acceptodds
Under review as a conference paper at ICLR 2027

Repair Inference after Representation-Alignment Failure

Abstract

When a representation-alignment correction underperforms a task reference, which tested repair recovers more, and can the repair family reach that reference? We study this post-failure repair inference through matched component replacements and exact optimization over positive-scale repair paths. In THINGS-EEG2 image retrieval from electroencephalography (EEG) signals, we attribute the change in the ridge–Procrustes accuracy gap between people included in and excluded from encoder training. Direction receives greater attribution at the cohort mean. Yet for excluded people, replacing ridge's radius (centered output length) with the Procrustes radius recovers 3.46 percentage points more accuracy on average than replacing direction. The advantage is positive in all ten. In OfficeHome image–text retrieval, we scale centered outputs of fixed maps before adding back the fixed mean. Even allowing a separate label-informed positive scale for every query, the exact optimum gains 27.62 percentage points over the fitted correction but remains 9.43 points below the unmodified reference. Scale choice alone therefore cannot restore reference performance on these paths. For a second EEG encoder, the exact label-informed per-query optimum exceeds its subject-centered reference by 7.96 points, establishing attainability. Matched replacements quantify the recovery forgone by following attribution to the weaker tested repair. Exact optima determine whether the declared scale family can recover the reference.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
representation alignment, repair identification, component attribution, repair capacity, multimodal retrieval, cross-subject transfer

Reviews

Among:
Shape:
1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_gyBQOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies two questions failure: whether the component receiving greater attribution also provides the larger repair gain, and whether any member of a fixed positive-scale family can recover a reference accuracy. The authors establish two post-failure conclusions that attribution and fitted performance alone leave unresolved. Matched component replacements quantify the accuracy cost of following attribution to the weaker tested repair.

Critical strengths

The component exchanges are concrete and interpretable. The positive-scale analysis also has a clear mathematical basis: candidate-score differences are affine in the scale, making exact winning-set calculations possible under the specified scoring and tie rules. The paper carefully distinguishes source-fitted rules from label-informed oracle capacities.

Critical weaknesses

The attribution and repair questions use different targets. Attribution explains the performance difference between included and excluded participants, while repair concerns only excluded participants. A change that helps both groups equally will cancel in the first comparison but still help the second. The radius gains—4.57 and 4.43 points—illustrate exactly this. Section 3.2 also says that attribution of the excluded-group loss agrees with the repair ranking. This makes the main finding less surprising than the framing suggests.

The OfficeHome result may depend heavily on the chosen map. The map retains only 44 of 512 dimensions. Showing that scaling its output cannot recover the original accuracy is valid, but how much does this tell us beyond the limits of that map? A comparison that preserves the remaining subspace would help.

The practical benefit of the capacity calculation is unclear. Source-task validation already chooses the unmodified representation on OfficeHome. On STAE, the positive result requires choosing a scale for each query using its label. Neither case shows how the analysis leads to a better repair decision without target labels.

Questions for authors
  1. After matching the attribution objective to excluded-role repair, what substantive attribution–repair discrepancy remains?
  2. Does the OfficeHome exclusion persist when the mapping preserves the complementary subspace or uses a regularized full-rank alternative?
  3. What concrete decision improves when exact capacity is available, compared with source-task validation and ordinary scale selection?
  4. Can the authors clarify which central quantities can be independently regenerated from per-query features and fitted maps, rather than checked from saved summaries or intervals?
Reviewer_M35dOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

This paper mainly studies the post-failure repair diagnosis problem after representation alignment correction fails (i.e., how to make decisions when the fitted alignment mapping performs worse than a simple reference baseline). The authors do not propose a new deployable alignment algorithm, but instead discuss repair choices through two core diagnostic analyses: First, in the THINGS-EEG2 EEG-to-image retrieval task, the authors compare replacing the direction and radius of centered outputs, claiming that cross-role attribution (the interaction attribution between subjects included in and excluded from training) points to a suboptimal repair component (direction), while actually replacing the radius brings a larger performance recovery (recovering 3.46 percentage points more on average); Second, in the STAE and OfficeHome tasks, the authors introduce test set labels to calculate the exact capacity upper bounds of the positive-scale family (the global common-scale upper bound UcU_c and the per-query optimal scale upper bound UqU_q), to judge whether positive scalar scaling alone has the potential to catch up with the reference baseline.

Critical strengths
  1. Detailed experimental records and reproducibility details: The paper clearly records the data access permissions and hypothesis freezing times (Timing contracts) at each experimental stage, and actively reports the negative results on the Cogitate UoB dataset where the component repair ordering could not be reproduced, showing good experimental transparency.
  2. Exact analytical solution for positive-scale paths: On the given 1D positive-scale ray, the authors transform cosine similarity ranking into linear inequality interval intersections, and use exact rational arithmetic to eliminate sampling blind spots of grid search and floating-point errors.
Critical weaknesses

This paper is an analysis-based paper and does not give clear future suggestions or deployable new selectors, so its value mainly depend on whether the analysis methods in this paper is reasonable. Looking at its two core findings, one is the relationship between attribution and improvement, and the other is the relationship between headroom and capacity, I found big problems in both of them, among which:

  1. First, on the relationship between attribution and improvement, the setting of attribution target by the authors have a serious logical mismatch. What the authors try to solve is the performance repair problem inside a single group of "subjects excluded from training (Excluded role)", but when they do the attribution, what they calculate is "the performance gap change between the included and excluded groups (i.e., the cross-role interaction term J=(r−t)included−(r−t)excludedJ = (r - t)_{\text{included}} - (r - t)_{\text{excluded}})". Actually, replacing the radius has almost the same large positive improvement for both included (+4.57 percentage points) and excluded (+4.43 percentage points) groups. Just because these two huge positive gains cancel out each other artificially when doing subtraction across groups (becoming -0.14 percentage points), it makes the radius looks very small in the cross-role attribution. If we follow the normal logic and directly attribute the performance loss inside the Excluded group which needs repair, the contribution of radius (-4.43 to -3.37 percentage points) is much larger than direction (-0.97 to +0.08 percentage points), so the attribution result and actual repair effect is totally consistent. Therefore, the core conclusion that "attribution will mislead repair choice" is completely an illusion created by the authors' mismatched setting of using "cross-group interaction attribution" to guide "single-group internal repair".
  2. Second, on the relationship between headroom and capacity, the capacity metric defined by the authors and the experimental mapping premise has obvious design flaws.
    • First of all, the core metric used by the authors to measure the highest recoverable capacity and support "retained recovery possibility (such as in STAE experiment)" is the querywise upper bound UqU_q. This metric allows every query in the test set to directly look at the ground-truth test labels, and separately pick an optimal scaling factor αi\alpha_i on the positive real axis that only belong to this sample. This kind of per-query oracle metric breaks the geometric consistency across samples. As long as there exist a very narrow accidental hit interval on the 1D ray, it will be counted as 100% correct, which artificially creates a falsely high "pseudo headroom" that is impossible to learn and realize in label-free testing. Once we go back to the more realistic common-scale upper bound UcU_c (21.56%), STAE also cannot reach the baseline level (DCR 22.32%), and its positive diagnosis conclusion of "exceeding the baseline" immediately fails.
    • Secondly, when proving OfficeHome cannot recover the baseline, the fixed linear mapping used by the authors only has a rank of 44 (Rank-44) in a 512-dimensional feature space, which already forcibly threw away the information of the other 468 orthogonal dimensions during the mapping stage, and the later repair only allows adjusting a single isotropic scalar α\alpha. On a subspace that has already been severely truncated by dimensionality reduction and lost most feature dimensions, proving that single-scalar scaling cannot catch up with the full 512-dimensional original feature baseline (T0T_0) is just a tautology that gets an inevitable failure under a preset information bottleneck, which lacks real diagnostic value.

Therefore, I think from the logic perspective, this analytical and diagnostic paper does not hold at all, so I cannot give a positive evaluation.

Questions for authors
  1. On single-group attribution vs. cross-group interaction attribution: Since the repair target is only to improve the accuracy of Excluded subjects, why not directly attribute the loss (r−t)excluded(r - t)_{\text{excluded}} inside the Excluded group, instead of taking a detour to attribute the cross-group interaction term JJ? Since radius and repair effect is completely consistent when attributing directly inside the Excluded group (i.e., no reversal happens), how do the authors justify that this "attribution reversal" is not caused by your own mismatched problem setting?
  2. On the practical meaning of UqU_q and the validity of STAE conclusion: Without proposing any label-free test-time scale predictor, the oracle upper bound UqU_q that relies on single-sample ground-truth labels contains a lot of unlearnable accidental hits. If we exclude this per-sample oracle setting and strictly use the global common-scale upper bound UcU_c as the evaluation standard, STAE (21.56% < 22.32% DCR) actually also fails to recover the baseline. Does this mean the real usable capacity conclusions for STAE and OfficeHome is actually the same?
  3. On the rank-deficient bottleneck in OfficeHome: The linear mapping in OfficeHome only keeps 44 dimensions (throwing away 468 out of 512 dimensions). Under the premise that 91% of the dimensions have already been directly erased by the mapping, to what extent does proving "1D scalar α\alpha scaling cannot recover the 512-dimensional original baseline T0T_0" reflect the limitation of scaling repair itself, or does it just reflect the inevitable information loss brought by the Rank-44 projection?
Reviewer_qANhOpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
1
Soundness
2
Read review
Paper summary

The paper asks what to do when a representation-alignment correction ends up below some reference method. It breaks this into two questions: which of the tested component replacements recovers more accuracy, and whether a given family of repairs can reach the reference at all. On THINGS-EEG2 EEG-to-image retrieval, the authors split ridge and Procrustes outputs into radius (length of the centered output) and direction, and swap them between the two maps. Attribution of the gap between encoder-included and encoder-excluded subjects points to direction, but for excluded subjects, swapping in the Procrustes radius recovers 3.46 pp more than swapping direction. For a "positive output scale" repair family, they compute exact upper bounds using test labels, with one scale per map (Uc) or one per query (Uq). On OfficeHome, even Uq stays 9.43 pp below the unmodified reference. For the STAE encoder, Uq is 7.96 pp above the reference.

Critical strengths
  • The question itself is reasonable: does the component that explains a performance gap also tell you what to fix? The authors answer it with matched, paired replacements, not just correlations.
  • The exact computation of Uc and Uq over all positive scales is done carefully (ties, zero-output scales, the unbounded segment), and the decomposition in Eq. 3-4 into unreachability, sharing loss and headroom is neat.
  • The authors are upfront about limitations. They report the failed UoB replication and say clearly that their bootstrap intervals are descriptive.
Critical weaknesses
  1. The main finding is narrow and does not replicate. The result that attribution favors direction while radius is the better repair comes from one encoder (TSconv) and ten subjects. On the matched UoB cohort with 46 subjects, the prediction fails at the mean and holds for 0 of 46 subjects (radius minus direction is -0.22 pp, with 21 positive and 23 negative). So it seems specific to one setup, and the paper does not say when we should expect it to hold.

  2. The conceptual point is not new. It is well known in causal inference and in the recourse literature (Mothilal et al., Ustun et al., Karimi et al., all cited here) that what explains a contrast is not necessarily what you should intervene on. In this paper the effect shows up in a two-component decomposition where a gain shared by both roles cancels out in the role contrast. Section 3.2 basically shows this follows from how the contrast is defined. I could not find an insight that carries over beyond this particular decomposition.

  3. The capacity analysis relies on test labels and does not lead to a usable procedure. Uc and Uq are oracle bounds. The negative OfficeHome result only says that rescaling fixed maps cannot reach the reference, and as the authors note, task validation already picks the unmodified reference there, so no decision changes. The positive STAE result only says a per-query oracle scale exists. Neither gives a label-free rule. The forecasts in Section 4.4 also tie with simply always predicting "retained" on both cohorts.

  4. Only one repair family is studied, a single positive scale applied to centered outputs. It would help to know if the framework says anything about the repairs people would actually try next, such as per-dimension scaling, low-rank corrections, or hubness-aware retrieval (CSLS, inverted softmax).

  5. The statistics are thin. Component results rest on 10 subjects with bootstrap intervals that are not refit and, by the authors' own description, not calibrated. Many claims are given as counts ("10/10", "8/10"), several contrasts were tested on cohorts that had already been analyzed (Table 1), and the PKU results are preliminary.

  6. I am not sure who the target audience is. The paper sits between EEG decoding and multimodal alignment, but I don't see a clear takeaway for either. Someone working on cross-subject EEG decoding or image-text alignment would probably not change what they do after reading it.

Questions for authors
  1. Can you describe when the radius-over-direction ordering should hold, e.g. in terms of hubness, ridge shrinkage, gallery size, or the size of the mean relative to the centered outputs? This might explain why UoB fails.
  2. Is there a label-free way to recover part of the STAE per-query capacity (Uq - Uc = 8.72 pp)? If not, what decision does the capacity analysis support that task validation doesn't already give you?
  3. Do the conclusions change for richer repairs than a single scale, such as per-dimension scaling or a CSLS-style correction?
  4. Could you add one table that says which results come from cohorts analyzed before the hypothesis was fixed and which are truly prospective?

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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